Ultra-Short Course Bedaquiline, Clofazimine, Pyrazinamide and Delamanid Versus Standard Therapy for Drug-Susceptible Tuberculosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ultra-Short Course Bedaquiline, Clofazimine, Pyrazinamide and Delamanid Versus Standard Therapy for Drug-Susceptible Tuberculosis (NCT05556746), a randomized phase 2 study. The primary outcome is Median Time to Stable Liquid Culture Conversion by Week 8.

2. Clinical Question

The trial is randomized, open-label and parallel-group. Its stated primary analysis is a superiority comparison of time to liquid culture conversion through 8 weeks. The comparison concerns the timing of a culture-based endpoint, not a direct measure of all aspects of tuberculosis recovery or long-term status.

The posted primary outcome gives a median time for each arm and a Cox regression hazard ratio. These describe different aspects of the time-to-event data: the medians mark the middle of the observed time distributions, while the hazard ratio compares event rates over the analysis period under the model. Neither statistic alone describes every participant's course.

The question is clinically and statistically specific: whether the assigned regimens differ in the time to meet the defined conversion criterion during the stated follow-up. The registry record does not report an analysis of all possible clinical outcomes as part of this primary question.

3. Trial Design

PRESCIENT is a Phase IIc, randomized controlled trial with a parallel-group design and no masking. Participants were assigned in a 1:1 ratio to BCZD or standard therapy. The registry lists enrollment as 94. The trial status is active, not recruiting; the listed start date is 2023-11-24 and primary completion date is 2025-06-12.

The experimental regimen combines bedaquiline, clofazimine, pyrazinamide and delamanid over 12 weeks, with the listed dose schedules varying by drug. The comparator starts with rifampicin, isoniazid, ethambutol and pyrazinamide for 8 weeks, then continues rifampicin and isoniazid for 18 weeks. The record describes standard weight-based doses for the comparator but does not give specific doses for those drugs.

The trial is open-label, so participants and study personnel were not masked to treatment assignment according to the registry. The record does not report whether outcome assessment or laboratory assessment was masked. Randomization can support a fair comparison of assigned groups, while lack of masking can matter for outcomes influenced by participant or clinician judgments. The primary endpoint is based on culture conversion, but the record does not provide further information about laboratory masking or other safeguards against assessment bias.

The primary analysis population is described as enrolled participants who were not late exclusions. A late exclusion is defined by screening, baseline study or Week 1 sputum cultures that failed to grow M. tuberculosis, or by RIF or INH resistance detected in baseline molecular or phenotypic testing results that became available after enrolment. The available description ends before specifying any further population details. The primary outcome values are reported for 45 participants in the BCZD arm and 47 in the standard therapy arm; the registry's total enrollment should not be treated as the denominator for every outcome.

Participants in the experimental arm with evidence of poor clinical response at the end of therapy were to be re-treated with standard TB therapy, according to the brief summary. The record does not give further operational details about how poor response was defined or how retreatment was incorporated into the primary analysis. It also does not report the trial's original sample-size justification or a full statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Randomization was stratified by presence of lung cavitation and HIV status

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Enrolled participants who were not late exclusions. Late exclusion is defined as screening, baseline study, or Week 1 visit sputum cultures failed to grow M. tuberculosis, or resistance to RIF or INH was detected from baseline molecular or phenotypic testing results that became available after enrollment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Median Time to Stable Liquid Culture Conversion by Week 8, measured over Measured through Week 8.

The primary endpoint is median time to stable liquid culture conversion, measured through Week 8. Culture conversion is defined as the first of two negative sputum cultures, consecutive or not, without an intervening positive culture. The definition also allows qualifying visits at which a participant cannot produce sputum and has no signs or symptoms of active tuberculosis to count toward conversion.

Time-to-event endpoints are used when the timing of an event matters and participants may reach that event at different times. In general, this approach can use information about both whether and when the event occurs during follow-up, rather than reducing the outcome to a single status at one visit. Interpretation depends on the event definition, the follow-up period and how incomplete observations are handled.

For this trial, liquid culture conversion is a microbiological measure relevant to the stated efficacy question. The time limit of Week 8 defines the primary observation window; the endpoint is not a measure of every later clinical outcome. The reported median is the middle of the observed time distribution in an arm. It does not mean that every participant converted at that time, and it does not describe the full spread of individual times.

The registry reports full ranges for the primary medians, with both arms extending from 1.0 to 8.0 weeks. Those bounds describe the reported range, not how many participants converted at each time. The Cox regression result adds a model-based comparison over time, but its interpretation relies on the event coding and model assumptions. The record names the regression method but does not report diagnostics or detailed handling of censored observations.

7. Results Posted in the Registry

• Arm 1 BCZD vs Arm 2 RHZE: hazard ratio 0.70 (95% CI 0.47–1.05), reported p = 0.930 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Median Time to Stable Liquid Culture Conversion by Week 12

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Arm 1 BCZD vs Arm 2 RHZE: hazard ratio 0.65 (95% CI 0.45–0.93), reported p = 0.980 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Arm 1 BCZD vs Arm 2 RHZE and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span time to stable culture conversion through Week 12, adverse events, a favorable composite outcome, premature treatment discontinuation, skin coloration and distress related to skin coloration, and QTcF changes. This range reflects several different domains: microbiological timing, safety, treatment completion, participant experience and an electrocardiographic measure.

The posted secondary time-to-conversion analysis extends the observation window beyond the primary endpoint and uses the same general time-to-event framework. Its reported median values are 8.0 weeks for BCZD and 6.0 weeks for standard therapy. The record also gives an inter-quartile range and a Cox estimate. Those details should be considered alongside, not in place of, the Week 8 primary analysis. Other secondary outcomes are listed, but their numerical results are not reported in the registry record.

There is not enough posted numerical information to describe a consistent direction or overall pattern across all secondary endpoints. The names of outcomes alone do not show whether the arms differed, how precisely they differed or whether any differences were favorable. The secondary findings therefore cannot be used to complete an efficacy or safety narrative beyond the results actually reported.

In general, multiple secondary comparisons raise multiplicity concerns: when many outcomes are tested, the chance of at least one apparently notable result can increase if no adjustment is made. The registry record does not report a multiplicity adjustment or a hierarchy for secondary outcomes. Accordingly, secondary results generally carry less confirmatory weight than a prespecified primary result, especially when the number of tests, analysis choices and adjustment strategy are unclear. They can still inform interpretation and future study questions, but should not be treated as independent confirmation of the primary finding.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Cumulative Probability of Experiencing Any Grade 3 or Higher Adverse Event (AE)
• Cumulative Probability of Having a Favorable Composite Outcome
• Proportion Who Prematurely Discontinue Treatment
• Median Time to Stable Liquid Culture Conversion by Week 12
• Mean Change in Skin Coloration Since TB Treatment Started at Weeks 8, 12, 16, 26, 60, and 86
• Mean Distress Related to Skin Coloration Since TB Treatment Started at Weeks 8, 12, 16, 26, 60, and 86
• Mean Change in QTcF From Baseline to Week 1, 2, 4, 8, 12, and 16
• Mean Change in QTcF From Baseline to End of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome: time from the relevant study origin to the defined culture-conversion event, assessed through Week 8. The registry names Cox regression as the method for the comparison. In general, Cox regression models the event rate over time while allowing the baseline rate to vary, and expresses the comparison between groups as a hazard ratio. The record does not specify the time origin, covariates, stratification, or exact handling of observations without a recorded conversion.

What does a hazard ratio describe?

In general, a hazard is the instantaneous event rate among participants who have not yet had the event, conditional on the model and remaining under observation. A hazard ratio compares that rate between groups. It is not a ratio of medians, a difference in weeks, or a direct estimate of the proportion converting by a particular visit. A value of 1.0 is the conventional no-group-difference reference for a hazard ratio. Values below or above that reference indicate different estimated event rates, with direction depending on which group is in the numerator and how the event is coded.

The reported primary hazard ratio is for BCZD versus standard therapy. Because the event is conversion, the usual event-rate interpretation treats a ratio below 1.0 as a lower conversion event rate in BCZD relative to standard therapy, under the model. This interpretation is conditional: the estimate can be affected by the event definition, analysis population, follow-up and model assumptions. The registry does not report proportional-hazards diagnostics or other model checks, so their adequacy cannot be assessed from the record.

Why report medians as well?

A median time is the point at which half of the relevant time distribution lies on either side, subject to the analysis definition and available observations. It is an easily interpreted summary of timing, but it compresses the data. Two groups can have the same median and different distributions, or different medians while having substantial overlap. The registry gives full ranges for the primary outcome and inter-quartile ranges for the secondary Week 12 outcome. A range reports the observed endpoints; an inter-quartile range describes the middle half of a distribution. Neither alone describes the shape of the full distribution.

In general, time-to-event analysis can account for observations whose event time is not observed within the analysis window through censoring methods. The record does not say how many observations were censored, how censoring was defined, or what assumptions were used. It is therefore not possible to determine from the posted description how censoring affected the estimates.

How should the confidence interval and p-value be read?

A confidence interval gives a range of estimates compatible with the data and the statistical procedure at a stated confidence level. In repeated use of a method under its assumptions, intervals constructed in this way have the stated coverage; a particular interval is not a probability statement about the true value. For a hazard ratio, 1.0 is the no-difference reference. The primary interval runs from 0.465 to 1.050, so it includes that reference. The reported confidence level is 90%, not 95%.

A p-value describes how unusual results at least as incompatible with the null model as the observed result would be if that model and the test assumptions held. It is not the chance that the null hypothesis is true, and it does not measure clinical importance. The registry reports p-values for the Cox analyses but does not identify the test statistic, whether the test was one- or two-sided, or the precise adjustment and variance procedures. Those details are not reported in the registry record.

The Week 12 secondary analysis reports a confidence interval that does not include 1.0 together with a p-value of 0.98. Under common inferential conventions, those figures would not ordinarily imply the same conclusion. Since the record does not explain the pairing, the numbers should be presented as recorded and not silently reconciled. This observation does not license replacing the sponsor's analysis with a newly calculated result.

What does open-label allocation affect?

Random allocation helps make treatment groups comparable in expectation, but open-label treatment means assignment was not masked. In general, lack of masking can influence behaviors, co-interventions, reporting and judgments. The endpoint uses laboratory cultures, which are less subjective than some outcomes, but the registry does not describe laboratory masking, assessment procedures or other protections against bias. The record also does not state whether the Cox model adjusted for baseline factors or whether the primary analysis followed intention-to-treat principles.

These method details matter because the numerical summaries are not self-sufficient. Their meaning depends on who was analyzed, how follow-up and missing observations were handled, how the event was defined, and whether model assumptions were reasonable. The record supplies the outcome definition, population description and named regression method, but does not report all of those supporting details.

11. Confidence Intervals and Precision

The primary hazard ratio is 0.699, with a 90% confidence interval from 0.465 to 1.050. The interval includes the no-difference reference of 1.0 and covers values that point in different directions relative to that reference. This means the estimate is not precise enough to exclude no difference at the stated confidence level. It also spans a range of possible relative event-rate estimates, rather than identifying one exact effect.

The 90% confidence interval should not be read as a 90% probability that the true hazard ratio lies between its endpoints. In general, a confidence interval describes the performance of an interval-producing procedure over repeated studies under its assumptions. For one trial, it communicates the uncertainty associated with the estimate and method.

The median times provide a different kind of summary. The primary medians are 8.0 weeks for BCZD and 6.0 weeks for standard therapy, and both reported full ranges extend from 1.0 to 8.0 weeks. These range limits alone do not establish how concentrated or dispersed the times are within the intervals. The number of participants with event times at each point is not reported in the registry record.

For the Week 12 secondary analysis, the reported 90% confidence interval is 0.449 to 0.932, while the p-value is 0.98. The record does not explain this apparent mismatch under common testing conventions. It is important not to select whichever statistic supports a preferred reading; both should be identified as reported, with the lack of clarification noted.

Precision is also limited by information not described in the record, including the number of events, censoring pattern and model diagnostics. These omissions prevent a fuller assessment of how the estimates were supported. The interval expresses uncertainty under the reported analysis, but it does not capture every possible source of bias or uncertainty.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations are based on the observed effect, not on the trial's original design. For these time-to-event comparisons, the displayed figures are total events, not participants per arm. This differs from sample-size illustrations for outcomes where the figures are stated as participants per arm.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses the stated fraction of the observed effect as the effect to detect. The registry does not report the trial's own original design assumptions or sample-size justification.

The 80% power column describes the total number of events that a planning calculation estimates would be needed for an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding planned event count for a 90% chance. These are design quantities, not observed results. A smaller target effect requires more events to distinguish it from the null under otherwise unchanged assumptions; the illustrations therefore increase the required event count when planning for 75% or 50% of the observed effect rather than 100%.

Because the figures are total events, they should not be read as the number of participants in each arm. Event counts and participant counts are not interchangeable in time-to-event studies: participants can have different follow-up and not all necessarily experience the event during observation. The record does not give the event accrual or follow-up assumptions used in these illustrations beyond those.

These calculations are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimate and its uncertainty after results are available. The confidence interval, event definition, analysis population and limitations of the reported model are more informative for understanding what the trial data support.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.699, so ln(HR) = -0.3581.
2. d = 4 × (1.96 + 0.842)² / [ln(0.699)]² = 244.8, rounded up to 245 events in total for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
hr <- 0.699                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(5556746)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 245 (80% power), 328 (90% power)
 75% of observed effect: events = 436 (80% power), 583 (90% power)
 50% of observed effect: events = 980 (80% power), 1,311 (90% power)
Simulated power with 245 events: 0.804 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 340 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 94 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 1.38461538461538          # control-arm median, months (converted from the posted unit)
hr          <- 0.699          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis              Value Efficacy
   IA 1: 33%                  Z   3.7103
      N: 148        p (1-sided)   0.0001
 Events: 111       ~HR at bound   0.4936
   Month: 10   P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.7   0.0338
   IA 2: 67%                  Z   2.5114
      N: 260        p (1-sided)   0.0060
 Events: 221       ~HR at bound   0.7133
   Month: 18   P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.7   0.5603
       Final                  Z   1.9930
      N: 340        p (1-sided)   0.0231
 Events: 332       ~HR at bound   0.8034
   Month: 60   P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.7   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor's reported primary comparison uses Cox regression and gives a hazard ratio of 0.699, a 90% confidence interval from 0.465 to 1.050, and p-value of 0.93. Those are the reported analysis results. No discrepancy is flagged in the registry record, and no alternative recalculated estimate is needed to describe them.

The ratio is reported for BCZD versus standard therapy. Under the usual interpretation for time to conversion, a ratio below 1.0 indicates a lower event rate in the BCZD arm during follow-up, conditional on the model. The interval includes 1.0, so it does not exclude the conventional no-difference value at the reported confidence level. The median times are also reported: 8.0 weeks for BCZD and 6.0 weeks for standard therapy. Those summaries describe the middle observed times and are not interchangeable with the hazard ratio.

The sponsor's p-value should be quoted as reported, not treated as an effect size or as the probability that the null is true. The registry does not provide the full test specification or enough detail to reproduce the sponsor's analysis. Therefore, any simple unadjusted recalculation from summary statistics would not replace the model-based result. The sponsor's own analysis is the relevant reported inferential analysis for this endpoint.

The Week 12 secondary analysis likewise reports a Cox hazard ratio, confidence interval and p-value. The record does not explain the apparent inconsistency between that interval and p-value under common conventions. The values are best treated as a registry-reporting issue requiring clarification, rather than resolved through an unreported recalculation.

16. Multiplicity, Missing Data and Analysis Populations

The primary efficacy question is time to liquid culture conversion through Week 8. The record also lists numerous secondary outcomes and reports a Week 12 time-to-conversion analysis. Testing multiple outcomes can increase the chance of at least one result appearing notable even when there is no underlying difference. In general, multiplicity can be addressed through a prespecified hierarchy, adjustment of significance thresholds, or interpretation that treats secondary comparisons as exploratory. The registry record does not report which approach, if any, was used.

The record does not report a full statistical analysis plan, a hierarchy among secondary outcomes, or an adjustment for multiple comparisons. It also does not explain whether any analyses were prespecified before unmasking or how missing outcome data were handled. These details are not reported in the registry record, so it is not possible to assess their effect on the interpretation.

The primary population excludes late exclusions, which are defined by specified sputum culture and resistance findings. Beyond that description, the record does not report the full analysis-population rules. It does not state whether participants were analyzed according to randomized assignment, whether there was a per-protocol analysis, how treatment discontinuation affected follow-up, or how retreatment for poor response was handled analytically.

For time-to-event analyses, incomplete follow-up may lead to censoring. In general, standard methods rely on assumptions about the relationship between censoring and the event process. The record does not report the number or reasons for censored observations, missing culture results, or sensitivity analyses addressing missingness. Nor does it give enough information to evaluate whether the approach to censoring differed by arm.

These omissions do not invalidate the reported estimates, but they limit independent appraisal. The named Cox regression method and outcome definition identify the broad analysis approach, while unreported details leave uncertainty about implementation and robustness. The reported p-values and confidence intervals should therefore be interpreted as registry results, not as a complete account of every analysis decision.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: sepsis (2.2%), tuberculosis (2.2%), femur fracture (2.2%), acute leukaemia (2.2%), delirium (2.2%).

The registry reports serious adverse events among 46 participants at risk in the BCZD arm and 48 participants at risk in the standard therapy arm. Serious adverse events affected 4 participants in the BCZD arm and 0 in the standard therapy arm. The record reports 2 deaths in the BCZD arm and 0 in the standard therapy arm. These counts describe the posted safety record; they do not establish that treatment caused or prevented an event.

The most frequently listed serious adverse event terms are sepsis, tuberculosis, femur fracture, acute leukaemia and delirium, each reported as 2.2%. The record does not provide further information about event timing, severity details, relatedness assessments, or whether a participant could contribute more than one event term. The terms should not be added to infer a total, since overlap and counting rules are not reported.

Safety findings are descriptive and require context, including follow-up duration, definitions, exposure and attribution. The available counts do not support a causal comparison on their own. The registry lists safety as a key secondary outcome, but a fuller interpretation would require the complete adverse-event reporting and analysis details, which are not reported in the registry record.

18. What the Result Does, and Does Not, Mean

The posted primary data describe median time to stable liquid culture conversion through Week 8 and a Cox regression comparison between the randomized arms. The median was 8.0 weeks for BCZD and 6.0 weeks for standard therapy. The reported hazard ratio was 0.699, with a 90% confidence interval from 0.465 to 1.050 and a p-value of 0.93. The interval includes the no-difference reference, leaving substantial uncertainty about the relative event rate.

These results do not establish that one regimen is superior on the primary endpoint. Nor do they establish that the regimens are equivalent: a failure to exclude no difference is not evidence that all clinically relevant differences have been ruled out. Equivalence or non-inferiority requires an appropriate design, margin and analysis; those are not reported as the primary question.

The observed medians and hazard ratio answer a narrow question about the timing of a defined culture-conversion event in the stated population and follow-up window. They do not by themselves establish effects on cure, relapse, transmission, quality of life, or long-term clinical outcomes. Such outcomes should not be inferred from culture conversion alone.

The trial is open-label, and the available description does not include all details needed to assess analysis populations, censoring, missing data, model assumptions or multiplicity. The registry also does not report numerical results for most listed secondary outcomes. These limits constrain how broadly the posted findings can be interpreted.

Finally, the results should not be turned into medical advice or generalized automatically beyond the trial population. The record identifies a Phase IIc study and reports enrollment of 94, but outcome denominators and the primary analysis population are described separately. The posted estimates are evidence from this trial record, not a complete basis for treatment decisions or claims about other settings.

19. Why This Trial Matters Statistically

This trial raises a useful statistical issue: a time-to-event endpoint can produce several summaries that appear to tell different parts of the story. A median describes a central time, a range describes observed endpoints, and a hazard ratio compares model-based event rates across follow-up. They answer related but non-identical questions, so interpretation should not rely on just one statistic.

The primary median is later in the BCZD arm than in the standard therapy arm, while the hazard ratio is below 1.0 for BCZD versus standard therapy. For a conversion event, that direction is consistent with a lower event rate under the usual hazard interpretation. Yet the primary confidence interval includes 1.0 and the reported p-value is 0.93. Together, these statistics illustrate why a point estimate or median difference should not be treated as decisive evidence without considering precision and analysis assumptions.

The record also illustrates the importance of clearly aligned inferential reporting. The Week 12 secondary analysis pairs a confidence interval that excludes 1.0 with a p-value of 0.98. Since the registry does not explain that relationship, readers need to preserve the reported values and recognize the uncertainty rather than silently resolving it.

Open-label randomization, the defined exclusion population, and incomplete reporting of censoring and analysis details also matter statistically. Randomization is valuable, but it does not eliminate every concern about outcome assessment, missing information or model assumptions. Explicit reporting of these elements helps readers evaluate whether the estimates answer the intended question.

Finally, the range of secondary outcomes shows why a clear hierarchy and multiplicity plan matter. A broad outcome set can provide useful safety and participant-experience information, but unadjusted comparisons may be less confirmatory. Distinguishing the primary analysis from supportive or exploratory results is central to responsible interpretation.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the full statistical analysis plan, including the time origin for the primary time-to-event outcome, model covariates, proportional-hazards checks, censoring rules, or sensitivity analyses. It also does not report the number of primary events or the pattern of follow-up and missing culture results. These omissions limit assessment of the Cox model and the precision of its result.

The primary analysis population excludes late exclusions based on culture growth or resistance findings, but the record does not provide all population rules or clarify how the analysis relates to randomized assignment. The posted primary outcome counts are 45 and 47, while the enrollment figure is 94; the record does not explain all reasons for the difference between enrollment and outcome denominators. Results should therefore be read with attention to the stated analysis population rather than assuming every enrolled participant contributed to every endpoint.

The study is open-label. The registry does not report whether laboratory personnel or outcome assessors were masked, nor does it provide details of procedures to limit assessment bias. It also does not report the original sample-size justification, so the planning illustrations based on the observed effect should not be confused with the trial's prospective design rationale.

Numerical results for most secondary outcomes are not reported in the registry record, and no multiplicity strategy is described. The Week 12 analysis reports a confidence interval and p-value that do not appear aligned under common conventions, without an explanation. Serious adverse event counts are provided, but detailed attribution and overlap information is not reported. These limitations do not change the posted numbers; they narrow the conclusions that can be drawn from them.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Ultra-Short Course Bedaquiline, Clofazimine, Pyrazinamide and Delamanid Versus Standard Therapy for Drug-Susceptible Tuberculosis — NCT05556746.
• Registry record last updated 2026-08-05; status last verified 2026-07.
• Results first posted 2026-08-05.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

NCT05556746, PRESCIENT, is a Phase IIc, randomized, open-label, parallel-group trial comparing a 12-week BCZD regimen with standard therapy for drug-susceptible pulmonary tuberculosis. The registry lists enrollment of 94, status active, not recruiting, and primary completion on 2025-06-12.

The primary endpoint is median time to stable liquid culture conversion through Week 8. Reported medians are 8.0 weeks for BCZD and 6.0 weeks for standard therapy. The Cox hazard ratio is 0.699, with a 90% confidence interval from 0.465 to 1.050 and p-value of 0.93. The interval includes 1.0, and the registry does not report enough methodological detail to resolve all questions about implementation or precision.

The record lists safety and several other secondary outcome domains, but numerical results for most are not reported. The available findings describe this trial's posted outcomes and should be interpreted within the stated population, endpoint definition, follow-up and reporting limitations.